Agency Problems, the 17th Amendment,
and Representation in the Senate
Sean Gailmard University of California, Berkeley
Jeffery A. Jenkins University of Virginia
A prominent change in American electoral institutions occurred when the 17th Amendment to the Constitution established
direct election of U.S. Senators as of 1914. How did this change the political agency relationship between the mass electorate
and U.S. Senators? We develop theoretical expectations about the representational effects of direct election by a relatively
inexpert mass electorate and indirect election by a relatively expert political intermediary, based on principal-agent theory.
The chief predictions are that the representative will be more responsive to the mass electorate under direct election, but will
also have more discretion to pursue his or her own ends. We use the 17th Amendment as a quasi-experiment to test the
predictions of the theory. Statistical models show strong support for both predictions. Moreover, the 17th Amendment is not
associated with similar changes in the U.S. House of Representatives—as expected, since the amendment did not change
House electoral institutions.
A
cornerstone of theoretical justifications for representative government is that representatives
faithfully translate popular will into policy decisions, and constituents are able to hold them accountable through elections if they do not. Even if voters are
fully informed and rational, the blunt instrument of elections may not be up to this task, and if they are not, then
any decoupling of citizens from policy decisions is inherently problematic (although perhaps necessary in a large
democracy). Furthermore, placing extra intermediaries
between citizens and ultimate policy choices linked by a
chain of electoral connections would seem to make matters worse for citizens because every link in the chain is
another possibility for a disconnect between voters and
policy choices. However, this logic is complicated if electoral intermediaries hold better information than voters
about selecting or monitoring elected officials. The intermediaries’ information is useful for voters, although
they may not leverage it exactly as voters would if they
themselves had it.
The 17th Amendment to the U.S. Constitution provides a unique opportunity to study such institutional
effects and trade-offs in representation. Enacted in 1913,
the 17th Amendment changed the basis of election of U.S.
Senators from the state legislature to a statewide popular
vote. A simple principal-agent argument posits that the
amendment made senators direct agents of their ultimate
principals, state voters, rather than indirect agents directly
accountable to political intermediaries in the state legislature. Put differently, the amendment replaced indirect
control with direct accountability, of which the chief implication is that senators should be more responsive to
the state electorate’s preferences directly.
We believe this simple agency logic is partly right,
but that it misses an important factor. That is, in terms of
democratic accountability of senators to their state electorates, direct election involves a trade-off. While the 17th
Amendment did create a direct agency relationship, it also
eliminated both the informed selection and monitoring
of U.S. Senators by relative political experts, state legislators. Therefore, U.S. Senators may have been held to
a better postamendment standard in democratic terms,
but not as tightly as they were held to their preamendment standard. Which arrangement is better normatively
Sean Gailmard is Assistant Professor, Charles and Louise Travers Department of Political Science, University of California, Berkeley, 210
Barrows Hall, Berkeley, CA 94720 (gailmard@berkeley.edu). Jeffery A. Jenkins is Associate Professor, Woodrow Wilson Department of
Politics, University of Virginia, Charlottesville, VA 22904 (jajenkins@virginia.edu).
A previous version was presented at American University, Caltech, Duke, Florida State, George Mason, Harvard/MIT, Notre Dame, Penn
State, SUNY-Buffalo, Texas A&M, the University of Chicago, the University of Iowa, the University of Virginia, William & Mary, the 2005
meeting of the Midwest Political Science Association, and the 2006 NBER Development of the American Economy Summer Institute. We
thank the audiences and Scott Ainsworth, Chris Berry, Fred Boehmke, Doug Dion, Erik Engstom, David Epstein, Jeff Grynaviski, Sam
Kernell, Jeff Milyo, Roger Myerson, John Patty, Dave Primo, Wendy Schiller, Chuck Shipan, and Craig Volden for helpful comments.
American Journal of Political Science, Vol. 53, No. 2, April 2009, Pp. 324–342
C 2009,
324
Midwest Political Science Association
ISSN 0092-5853
AGENCY PROBLEMS AND THE 17TH AMENDMENT
depends on whether one wants a reliable shot that misses
the bull’s-eye, or an erratic shot that sometimes hits. Before this issue can even be broached, however, it is necessary to establish that our version of the agency theoretic
account is empirically useful.
Our theoretical discussion has several implications
that we test using scaled roll-call voting decisions of
U.S. Senators in presidential election years from 1880 to
1940 as a measure of senator behavior, state-level Republican two-party presidential vote share as a proxy
for state electoral “ideology” or policy preferences, and
the Republican share of the joint convention in the state
legislatures as a proxy for state legislative policy preferences. In particular, our argument implies that U.S.
Senators should be responsive to state legislative preferences before the 17th Amendment, but less so afterward. It implies that—conditional on state legislative
preferences—U.S. Senators should not have been especially responsive to state mass electorate preferences before the amendment, but should have been responsive
afterward. Finally, our theory implies that the difference
in roll-call records within a given state’s Senate delegation
should be greater, again conditional on state ideology, after the 17th Amendment than before it—because senators
were no longer selected by and accountable to political
experts. We find strong support for these hypotheses,
with the effects being significant both statistically and
substantively.
Our research design uses the 17th Amendment as a
treatment in a quasi-experimental sense and compares
observations without treatment (before the amendment)
to those with it (after the amendment). However, other
political developments contemporaneous with this treatment could in principle account for the results. Therefore, we also explore contemporaneous changes in the
U.S. House of Representatives, a close comparison group
not subject to the treatment we explore, but that is buffeted by the same confounding factors that could threaten
the validity of our causal inferences. We find that the 17th
Amendment is not associated with changes in the House
similar to those we find in the Senate.
The rest of the article is organized as follows. We first
begin by briefly developing the issue and reviewing related literature. We then lay out the theory behind our
argument, followed by a discussion of the empirical measures and methods we use in a statistical test of several
implications of our theory. Our empirical analysis of the
17th Amendment comes next, and then we further address the institutional mechanisms behind the effects we
observe and apply our models to the House as an untreated comparison group. Finally, we conclude.
325
Electoral Institutions, Direct
Election, and the 17th Amendment
A crucial plank in the normative defense of representative
democracy is that elections help to translate popular preferences into public policy decisions. Given such factors as
“rational ignorance” and information asymmetries faced
by the mass electorate (Arnold 1993; Downs 1957), potential incoherence of mass electorate ideology (Campbell et
al. 1960), and the development and biases of special interests in the United States (Baumgartner and Leech 1998),
whether and how institutions cause this translation is not
obvious.1 Therefore, a number of scholars have offered
theoretical and empirical analyses of electoral institutions
in light of these troubling issues.
The questions amount to whether elections in realworld settings of limited choice, hidden actions by representatives, and hidden information about their goals
and values offer a potent enough device for voters to
(i) monitor and electorally sanction representatives who
take undesired actions, and/or (ii) select representatives
who want to take desired actions even when they are not
induced to do so by monitoring and sanctions. If the
answer to these questions is yes, then from a principalagent standpoint voters can be said to “control” their
elected representatives.2 These questions gave rise to the
principal-agent theoretical perspective on elections, and
their consequences for representation and accountability.
The pioneering contributions of Barro (1973) and Ferejohn (1986) focused on monitoring and electoral defeat
as a sanction. Banks and Sundaram (1993, 1998) and
Fearon (1999) have substantially enriched the theory by
including the issue of selection as well as sanctioning. The
crucial agent incentives in the theory of indirect and direct election that we develop can be generated by either
the selection or sanctioning aspects of elections, and we
will return to this dual role of electoral institutions below.
The American context offers several types of variation
in electoral institutions that scholars have leveraged to
1
Of course, several important analyses have shown a link between
constituency preferences or characteristics and the behavior of
elected officials (e.g., Bartels 1991; Miller and Stokes 1963). However, these findings do not imply that the institution itself causes
the link. To take an extreme and dim view of the incentives generated for elected officials, the same sort of link would appear even
if elections had no incentive effects at all and representatives were
selected at random from their constituencies. Thus, our purpose
is not to establish a link between constituents and representatives,
but to understand the institution’s role in making it.
2
We do not, therefore, use the word “control” to imply more than
this, or any degree of domination of elected representatives by
voters.
326
analyze their role in mediating political agency relationships. A common empirical strategy is to compare the
policy decisions made by public officials, such as judges
or regulators, in states or political units in which they
are elected to units in which they are appointed. For example, Besley and Coate (2003) found that elected electricity regulators pursue policies one would suspect are
more favorable to the public than appointed regulators
do. Similarly, election of judges is associated with responsiveness of judges (as well as agendas in judicial elections),
whereas appointment is associated with judicial independence (Hall 2001; Hanssen 1999).3
This literature neglects two features of our analysis. First, it considers only the responsiveness of elected
agents to the populace or mass electorate, not the discretion of the agents with respect to their set of principals. But leaving selection and sanctioning to the mass
electorate implies a different level of information and
expertise in evaluation of elected agents (and potential
replacements), thereby affecting their discretion as well
as responsiveness. We think this is a crucial aspect of the
normative evaluation of electoral institutions, and an important consideration for analysis. Second, this research
typically assumes that no relevant factors affecting policy
decisions in question, but excluded from the model, are
correlated with the electoral institutions. Therefore, the
potential for confounding events or changes to appear as a
treatment effect of the electoral institution is great in these
research designs. In contrast, we explore the potential for
contemporaneous confounding events by comparing the
Senate and the House of Representatives.
One prominent change in American electoral institutions is of course the 17th Amendment. However, it has
elicited surprisingly few scholarly treatments.4 This may
be in large part due to the influence of Rogers (1926) and
Riker (1955), who argued that the 17th Amendment as
such was not a significant institutional change at all. These
scholars contended that it was instead largely anticlimactic, as a majority of states5 by 1912 had already passed
direct-primary laws that served as de facto direct-election
instruments.6
Even more rarely has the 17th Amendment been used
to analyze representation or the effects of electoral insti3
See Besley and Case (2003, 52–54) for a review of the related
literature.
4
Early treatments (Haynes 1906, 1938; Rogers 1926) tended to
focus on the causes of the amendment rather than its consequences.
5
Rogers (1926, 114) documented 29 such states. More recently,
Lapinski (2003) identified 30.
6
Lapinski (2003) and Schiller and Stewart (2007) recently developed the most direct evidence in contradiction to this argument.
SEAN GAILMARD AND JEFFERY A. JENKINS
tutions. Crook and Hibbing’s (1997) work is a notable
exception; they argued that direct election and the 17th
Amendment had a politically significant effect on representation in the Senate. In a set of aggregate analyses, they found that, after the amendment, senators were
more likely to have government experience, and Senate
elections more closely mirrored both House and presidential elections (on the latter point, see also Engstrom
and Kernell 2007). More recently, a small literature has
emerged that examines the effects of the 17th Amendment
on the behavior of senators. This research investigates
whether the change in individual senators’ underlying
constituency—from the state legislature to the state-level
populace—altered their behavior in office. And, in fact,
a majority of such studies conclude that a significant behavioral change consistent with a broadening “electoral
connection” occurred in the Senate (see Poole and Rosenthal 1997 on roll-call abstention rates; Lapinski 2003 on
retention of committee assignments; Meinke 2008 on
position taking; Bernhard and Sala 2006 on ideological
moderation over the electoral cycle; and Patty 2008 on
predictability of senator voting records; but Wawro and
Schickler 2006 find no effect).
To our knowledge, ours is the first 17th Amendment
study to explicitly connect senators with the geographic
units they represent, a level of analysis that similar research on the House of Representatives has shown to be
important for the study of representation (see, e.g., Bartels
1991; Canes-Wrone, Brady, and Cogan 2002; Miller and
Stokes 1963). This “dyadic” approach offers important insights that are not captured by studies that analyze either
the aggregate behavior of the Senate in relation to national
public opinion or the behavior of individual senators facing common electoral pressures (but not specifically tied
to their states’ preferences). The geographic unit is the
level at which electoral incentives operate, and where the
greatest potential exists for elections to translate policy
preferences in the electorate into policy decisions in government. These are the key concerns in our theoretical
approach.
Agency Relationships
in Representation: Theoretical
Expectations
The relationship between an electorate and its representative is, at least in part, a principal-agent relationship.
By this we mean that the electorate in representative government delegates decision-making responsibility to its
AGENCY PROBLEMS AND THE 17TH AMENDMENT
agent, the representative. Since the electorate cannot observe all the beliefs and dispositions of every candidate for
office, and cannot observe every decision (or its context
or alternatives) made by every elected official, it faces the
potential problems of (i) electing an agent who has ideological beliefs far from its own (“adverse selection”), and
(ii) inducing its agent to make decisions it likes (“moral
hazard”).7 The chief formal lever the electorate has to influence its agent’s preferences and behavior is, of course,
an election. Elections are useful both for selecting agents
whose preferences are compatible with the electorate’s
(Banks and Sundaram 1993, 1998; Fearon 1999) and for
inducing an agent with any given preferences to act in
accordance with the preferences of the electorate (Banks
and Sundaram 1998; Barro 1973; Ferejohn 1986). But
they are also blunt instruments of accountability.
The 17th Amendment changed the agency relationship between a state electorate and its U.S. Senators. Prior
to the amendment, under indirect election, the relationship was one of indirect or hierarchical agency—the principals selected an agent, who in turn selected another
agent—with both delegated selection and monitoring of
the second agent by the first. That is, state voters chose
their agents, the state legislators, who in turn chose another set of agents, U.S. Senators, on behalf of themselves
and the state electorate.
It must be noted that nineteenth-century state legislatures were not always thriving and active bodies. Turnover
was often quite high. Assemblies met part-time. Nevertheless there are several reasons to expect them to be
better positioned than the state mass electorate at one or
both of the tasks of selection and monitoring of a political agent—and our conjecture is not that they were good,
only that they were better. First, state legislators would
generally have been more politically sophisticated and
connected than the typical voter. This relative sophistication could arise in part because of a selection effect; it is
conceivably part of the reason one enters politics in the
first place. More concretely it could arise due to information sharing in social networks. Campbell (1980) notes
that ethnic networks commonly played a role in election to state assemblies and that legislators tended to live
in common quarters while the assembly was in session.
Each of these factors facilitates rapid transfer of relevant
information and would help even relatively short-term
legislators assimilate the modest information needed to
make informed judgments (Lupia and McCubbins 1998;
327
Popkin 1991). Campbell also notes (chap. 3) that state
legislators, while often “short timers,” had some local notability that would suggest both access to the requisite information to evaluate contenders for U.S. Senate, and the
skills necessary to do so. Finally, while nineteenth-century
state legislators did not typically spend many terms in the
statehouse, the phenomenon of “political careerism” was
much more common at this time than “legislative careerism” (Carson and Jenkins 2007; Kernell 2005). The
state legislature was one (usually short) stop on a longer
political career path from local to state to federal office
and back again. Thus short-term service in the statehouse
does not imply that state legislators were political novices
or irregularly involved in politics.
In combination these factors likely gave state legislators an advantage over the mass electorate for (i) selection of new or replacement senators, on the basis of better
knowledge of the ideology and values of hopefuls and candidates in their state’s political scene, and (ii) monitoring
sitting U.S. Senators, on the basis of a better grasp of what
they had done, how they had voted, and positions they
had espoused while in office.8 These abilities—which we
stress need only be relative for our argument, rather than
absolute or finely honed—would arise naturally from immersion in political information networks and attention
to politics simply as part of their (possibly part-time) jobs
and daily business. As experts on politics, at least relative
to the typical voter, they could keep a close eye on behavior in the Senate and select the “right” senators when
they so desired. Note that this argument does not depend
only on monitoring capabilities of preamendment state
legislatures; both selection and monitoring support the
same basic logic for our present purposes.
Second, and especially in case of a relatively inexpert state legislature, state legislators themselves may have
been controlled or strongly influenced by state party or
chamber leaders (Haynes 1938; but see Schiller and Stewart 2008). We contend that this essentially follows the
same line of our argument. In each case one actor selects
an agent to act on its behalf, then transfers that selection
right to another actor—who is unlikely to be as informed
about the pool of possible agents or their actions while
in office. The observable implication in either case is that
after the transfer of selection rights, the selected agent’s
preferences should become less strongly related to the
initial selector’s preferences, and more strongly related to
8
7
The agency problem in representation has been part of American
discussions on the issue since the founding of the republic. Representation is obviously a complex, multifaceted relationship; our
theory only requires a focus on this facet. Fortunately, if our theory
is wrong and this is not a crucial facet, it will fail empirically.
The selection aspect of our argument, in particular, dovetails with
Schiller and Stewart’s (2007) finding that state legislators faced a
nontrivial set of candidates to choose from, and their choice of U.S.
senator was definitely not pledged before the balloting. This helped
give state legislators scope to use their information about what
candidates stood for in making their selection of U.S. Senators.
328
the subsequent selector’s preferences. Moreover, the initial selector’s informational advantage should allow for
less variation of the agent around the selector’s preferences before the transfer of selection rights.9 In sum, these
relative advantages in either selection or monitoring (or
both) would allow the state legislature, or the subset of
elites dominating the state legislature, to select and monitor its U.S. Senators relatively tightly in terms of its own
standard of behavior.
Thus the state electorate was essentially forced, before
the 17th Amendment, to delegate the selection and monitoring of U.S. Senators to the relative political experts in
the state legislature. In terms of representation, the major problem with this arrangement is that the state legislature’s (or controlling faction’s) preferred standard of
behavior need not be the mass electorate’s preferred standard of behavior. Because elections are blunt instruments
of selection and control, and mass elections typically have
a small number of candidates, the state electorate must
incur some “agency losses” relative to first-best, perfect
control of the decisions of the state legislature. This is because opportunistic state legislators or party bosses can be
expected to have substituted, to some extent, their own
preferences for those of the state electorate in decision
making. The existence of agency losses in state-level representation simply means that the electorate would not
have made exactly the same decisions as the electorate’s
agents in the state legislature, had the electorate possessed
the same resources and information as the state legislature.10 This is perforce true about the selection of U.S.
Senators by the state legislature.11
Putting these arguments together, viewing pre-17th
Amendment U.S. Senators in terms of hierarchical agency
with delegated selection and monitoring implies that they
would hew relatively closely to a standard determined
by the state legislature—either because of good selection
from a field of candidates or effective monitoring—but
9
Where this argument does fall apart is when the titular “agent” is in
fact selecting the titular “principal” before the transfer of selection
rights to the electorate, as has been argued about U.S. Senators and
state legislators prior to the 17th Amendment (e.g., Riker 1955). If
this were in fact the true version of events, our empirical analysis
would find no significant support for our theory.
10
A more familiar example helps make the point: compare to the
case of party convention delegates, who are both more ideological
and more informed than voters in general or even party voters.
This creates a scope for agency loss in framing party platforms and
selecting candidates whom voters have been unable to completely
eliminate.
11
Note, therefore, that we do not assume that the only or major
difference between the mass electorate and state politicians is their
level of information about U.S. Senators, though that is one important difference for our theory.
SEAN GAILMARD AND JEFFERY A. JENKINS
that this standard may not be the one chosen by the median in the mass electorate.
The 17th Amendment made the terms of the agency
relationship quite different. Instead of indirect agency,
the principal-agent relationship between voters and U.S.
Senators was obviously more direct. Voters no longer had
to rely on an imperfectly controlled intermediary to hold
a further downstream agent to account for them. Instead,
they themselves could select new U.S. Senators and try to
induce desired behaviors from sitting senators with any
given ideology, based on their own preferences. To the
extent that voters were informed about the preferences of
new Senate candidates or the behavior of sitting senators,
they could hold them accountable just as well as state
legislatures could—and hold them to a better standard
(from their own point of view, and from a normative
democratic point of view).
Of course, the information needed for that level of accountability was probably not as easily accessible by voters
as by state legislators. Voters can use cues, opinion leaders, and heuristics to get a reasonable general idea of the
position and actions of politicians (both prospective and
sitting ones), but because of both “rational ignorance”
and lack of practice they are probably not as precise in
their estimations as politicians are about each other. That
lack of information, or lack of context for the information that is available, attenuates control and reintroduces
scope for agency losses through a different route. Whereas
senators before the 17th Amendment might have been
well selected according to the “wrong” standard, after
the amendment they have been more loosely constrained
to the “right” standard, due to weaker selection and
monitoring.
To put it differently and somewhat crudely, consider
a thought experiment with p as the percentage of variance
in a senator’s behavior explained by variation in state legislature preferences, before the 17th Amendment. After
the 17th Amendment, part of p shifts to voters—some
percentage of variance q < p is explained, postamendment, by variation in mass electorate preferences. The restriction q < p comes from the assumption that selection
and monitoring are more effective when done by experts
than by novices. But the other part, p − q, shifts to the
individual senator herself, and is explained by variation
in her own preferences, variation in the preferences of
the reelection constituency she assembles (which may be
different after the amendment for different senators from
the same state), variation in the preferences of the political
network she assembled “on the way up,” her party leadership, etc. With agency losses between voters and state
legislatures, U.S. Senator behavior can be more closely
connected to the mass electorate’s preferences in general,
AGENCY PROBLEMS AND THE 17TH AMENDMENT
and yet more variable in general, after the amendment
than before it. On the one hand, a state’s U.S. Senate delegation should be on average more representative of the
state’s preferences, but on the other hand, its members
should exhibit greater differences relative to each other.
This agency theoretic view of the state-senator relationship has two testable implications regarding the effects of the 17th Amendment on representation in the
Senate.
H1 Responsiveness Effect: (i) A state’s senators should be
more responsive to the policy preferences of its mass
electorate after the 17th Amendment than before it.
(ii) A state’s senators should be less responsive to
the preferences of the state legislature after the 17th
Amendment than before it. This hypothesis follows
only from the change in political principals following
direct election, not their sophistication in selection
or monitoring.
H2 Increased Discretion Effect: A state’s senators should
exhibit greater differences in voting behavior from
each other after the 17th Amendment than before it.
If the electorate cannot select or monitor its agents
in the U.S Senate as effectively as political experts
can, the agents should be better able to pursue an
agenda other than that of their immediate principal (weaker monitoring), and more likely to want to
do so (weaker selection). This hypothesis depends
on the relative sophistication arguments we made
above.
Data and Empirical Methods
The hypotheses above imply that the 17th Amendment
caused a specific, measurable change in both the behavior of individual senators, and the differences in behavior within a state’s Senate delegation, as a function of
policy preferences of state-level political principals. Exploring this relationship empirically requires measures of
these variables. The unit of analysis for this measurement
is a senator-state-year for individual senator behavior,
and a state-year for differences within a state’s Senate
delegation.
We use DW-NOMINATE scores (Poole and Rosenthal 1997, 2001) for individual senators in presidential
election years from 1880 to 1940 as a measure of individual senator behavior. This is our dependent variable for
Hypothesis 1, the responsiveness effect. These scores are
the output of a technique that scales the roll-call records
of senators into a basic multidimensional policy space and
329
are explicitly designed to allow for dynamic comparisons
of the ideology exhibited in roll-call behavior. We use
only the scores from the first dimension of the recovered
policy space, which captures a more enduring, left-right
conflict present in every era of American politics (Poole
and Rosenthal 1997). The scale of the resulting scores
ranges from −1 to 1 (mean = 0.01, standard deviation =
0.41 in our sample period), with larger numbers implying
a more conservative roll-call record (Democrats average
about −0.33 over our sample period, Republicans about
0.34).12
The “within-delegation distance” for a state in a given
year (in presidential election years from 1880 to 1940),
tapping into discretion of senators, is the maximum difference13 between the first-dimension DW-NOMINATE
scores for any pair of members14 in the state’s Senate delegation for that year (mean = 0.25, standard deviation =
0.26). Its scale is 0 to 2. This is our dependent variable for
Hypothesis 2, the discretion effect.15
To measure state-level ideology or policy preferences
in the mass electorate, we use state-level Republican twoparty presidential vote shares, a common technique in
the literature (e.g., Carson 2005).16 Specifically, we use
the votes cast for the Republican presidential candidate
in a state as a percentage of votes cast for the Republican
and Democratic candidates in that state.17 This measure
12
All elected senators (or senators appointed but then elected) from
a state in a year are included in each state-year pair.
13
The mean pairwise difference in DW-NOMINATE scores in a delegation is very highly correlated (about 0.985) with the maximum
difference in scores in a delegation, so results are not sensitive to
using the maximum specifically.
14
Typically there were only two members per delegation per year,
but some states had three or even four senators in a session (due to
replacement of senators who depart mid-session) who cast enough
votes over their careers to have DW-NOMINATE scores. We omit
observations that include appointed senators who are not subsequently elected, as these senators are ostensibly not subject to the
accountability mechanisms we analyze.
15
Poole and Rosenthal (1984) first identified the empirical leverage
offered by within-delegation differences (in interest group ratings
of senator roll-call records), in their study of increasing polarization in the Senate over time. Schiller (2000) developed the most
comprehensive analysis of within-delegation differences in senator
behavior, in her demonstration that senators typically represent
different and often diverse interests from their common state.
16
A similar technique is used to generate a measure of district-level
ideology in studies of House members’ behavior. See Erikson and
Wright (2000) and Canes-Wrone, Brady, and Cogan (2002). Also
see Brady (2006) for a persuasive argument for using presidential
vote data in this way.
17
Election returns from a given year are matched with roll calls of
the senators serving in the Congress immediately subsequent to
that election, i.e., seated in the year following the election.
SEAN GAILMARD AND JEFFERY A. JENKINS
330
has several important benefits for our approach.18 Most
importantly, Republican presidential vote share is both
available and readily interpretable over the whole time
period under consideration. The measure is also parsimonious without doing too much violence to the complexities of ideology that are not central to our approach.
The Republican Party represented the “right” side of politics over the entire range of years, and with the exception
of the South (which we address with dummy variables),
both major parties were competitive in all states over this
time period. Scaled from 0 to 1 (mean = 0.48, standard
deviation = 0.18 over our sample period), larger values of
state-level Republican two-party presidential vote share
indicate a more right-leaning predisposition than smaller
values.19
We take the partisan composition of a state legislature in each year as a measure of state legislative policy preferences or ideology in that year (Burnham 1984).
Specifically, we use the Republican share of the “joint convention” in the state legislature in a given year (range 0–1,
mean = 0.49, standard deviation = 0.31 over our sample
period). This is the sum of Republican seats across (almost always) both chambers, divided by the total number
of seats in both chambers.
We focus on the period from 1880 to 1940 because
it encompasses the passage of the 17th Amendment and
should be long enough to detect regularities but not so
long that obvious “regime shifts” in American politics are
reflected.20 Before 1880, Southern Reconstruction dominated the national agenda and produced a deviation from
18
We also examine state Republican vote shares as deviations from
national average Republican vote shares in each year. This helps to
filter out the effects of unusually weak or strong candidates from
the major parties: even when the Democrat (for example) is very
weak, the relatively liberal states will have relatively liberal vote
shares. This has little effect on the empirical results.
19
Usage of state presidential votes is the reason why our data encompass presidential election years only. While other variables vary in
nonelection years, statistical models would necessarily be misspecified (assuming our theory is correct) by excluding state presidential
vote in nonelection years. It could be a useful robustness check to
use multiple imputation methods to fill in this missing data and
explore whether the results hold up. However, this is beyond the
scope of what we can accomplish in this article given space limits,
and we leave it for future research.
20
We match year t state legislatures with year t U.S. Senate roll calls.
If monitoring of U.S. Senators played a key role in their behavior,
in addition to selection, then the year t state legislature is indeed
a relevant principal and should be included in analysis of year t
U.S. Senator roll calls. Nevertheless, the year t-1 state legislature
may in fact have selected the year t U.S. Senator, so that this alternative matching is theoretically preferable. Thus we executed our
empirical analysis with the lag of a state’s joint convention share of
Republicans as the explanatory variable. While the estimated coefficients change, the substantive findings do not. In particular, our
findings in Tables 1 and 2 below continue to support the discretion
normal politics. After 1940, political competition changes
radically with the consolidation of the New Deal consensus, the politics of civil rights, and the rise of the Republican Party in the South. To avoid suspicion that observations from these periods taint the results, we leave them
out of the dataset.
Following Canes-Wrone, Brady, and Cogan (2002),
we pool observations from different years over time. This
creates a time series of observations for a collection of
cross-sectional units. A natural modeling approach for
data with this structure is (feasible) Generalized Least
Squares, assuming that errors may be correlated within
a single panel over time and differ in conditional variances across panels at a given point in time.21 This GLS
estimator is consistent even if observations/error terms
depart from independence and identical distribution in
this way.22 Additionally, as reported below, we replicate all
our analyses using OLS with state fixed effects (unbiased
for any such failures of i.i.d. observations) and PraisWinsten regression with state fixed effects (or, where justified, a more efficient GLS estimator with state random
effects).23 We defer further comment on the assumption
of pooling and other important robustness issues until
after the presentation of results.
Our research design is to take the 17th Amendment as a treatment and use a before-and-after comparison—untreated observations compared to treated
observations—to assess the treatment effects of direct
and responsiveness effects. Neither of these effects is supported for
the House of Representatives.
21
A state’s Senate delegation’s behavior is probably not independent
over time since its membership is durable and individual roll-call
behavior is persistent. Moreover, in the congress that encompasses
year t, the behavior of delegations from moderate states is clearly
more variable than the behavior of delegations from extreme states,
so heteroskedasticity is a potential issue as well.
22
Our dependent variables have limited range, making censoring
(a different failure of i.i.d.) a possible concern in principle. However, for individual DW-NOMINATE scores, only about 10% of the
observations are within one standard deviation of the scale boundaries. For within-delegation differences, we use natural logs in our
statistical models, which do have unlimited range (no observations
have a within-delegation difference of exactly 0, at which the natural log is undefined). We also check our results (as mentioned
in a subsequent footnote) in a GLM assuming a distribution
for within-delegation differences, which builds left-censoring into
the model. All of these factors considered, censoring is a relatively
minor issue and we neglect it for brevity.
23
We also replicated our results using OLS with panel-corrected
standard errors (Beck and Katz 1995). However, the contemporaneous correlation across units that helps this approach to outperform FGLS in comparative data is probably less of a factor in
our study, so we do not present these results below. Regardless, in
no case does OLS with PCSEs change our qualitative or principal
statistical findings.
AGENCY PROBLEMS AND THE 17TH AMENDMENT
331
TABLE 1 Regression Results: Senator DW-NOMINATE (First Dimension)
Scores
Explanatory Variable
State GOP pres. vote share
Interact., state GOP pres. vote
share and 17th Amendment
GOP joint convention share
Interact., GOP joint convention
share and 17th Amendment
17th Amendment indicator
South indicator
Time trend
Constant
N = 1221
OLS,
State FEs
FGLS
0.024
(0.078)
0.289∗∗∗
(0.108)
0.564∗∗∗
(0.056)
−0.481∗∗∗
(0.065)
−0.048
(.041)
−0.349∗∗∗
(0.030)
0.017∗∗∗
(0.003)
0.290∗∗∗
(0.049)
␹ 2 = 1554.5∗∗∗
0.162
(0.115)
0.596∗∗∗
(0.162)
0.583∗∗∗
(0.068)
−0.634∗∗∗
(0.089)
−0.143∗∗
(0.064)
–
0.024∗∗∗
(0.004)
0.232∗∗∗
(0.053)
F = 37.9∗∗∗
Within R2 = 0.17
Prais-Winsten,
State FEs
0.116
(0.121)
0.501∗∗∗
(0.169)
0.384∗∗∗
(0.074)
−0.551∗∗∗
(0.098)
−0.017
(0.060)
–
–
−0.187∗∗∗
(0.037)
F = 15.54∗∗∗
Within R2 = 0.07
Note: Unit of observation is a senator-state-year, 1880–1940. FGLS errors are assumed to be AR-1 within a
state’s time path and heteroskedastic across states in a given year. Standard errors are in parentheses.
∗
denotes significance at ␣ = 0.10, ∗∗ at 0.05, ∗∗∗ at 0.01.
election on an electoral agency relationship. We also take
the House of Representatives as an untreated comparison
group, which should not (according to our theory) be
affected by the treatment. This helps to strengthen our
assessment of the causal effects of the change to direct
electoral institutions.
Responsiveness and Discretion
of Elected Agents: Empirical Analysis
We analyze in turn the support for Hypotheses 1 and 2
in our evidence. This analysis will allow us to determine
whether the theoretical expectations set out above provide
a useful understanding of electoral institutions.
To test Hypothesis 1, we model senators’ DWNOMINATE scores as a function of Republican presidential vote share, Republican seat share in the joint convention, and their interactions with the 17th Amendment.
We include a South indicator variable and time trend
as controls,24 and an indicator for the 17th Amendment
24
The time trend is important because it separates autonomous
temporal changes in senator voting records from the treatment
effect of the 17th Amendment.
to ensure that the interaction terms do not erroneously
pick up an intercept shift due to direct election. Table 1
presents results from FGLS estimation, as well as OLS
regression and Prais-Winsten regression (assuming AR-1
errors within a state’s time path) with state fixed effects.25
The unconditional effect of the 17th Amendment on
senators’ voting records is negative in each model, but
uneven in magnitude and significant only in the OLSFE model.26 However, the crucial terms for Hypothesis
1 are the Republican two-party presidential vote share,
the Republican seat share in the state legislature, and
their interactions with the 17th Amendment. The uninteracted terms capture the effects of these covariates
before the 17th Amendment. As the responsiveness effect
implies, policy preferences in the state legislature had a
large and significant effect on senator roll-call records under indirect election. A 30 percentage-point increase in
25
Hausman tests reject the hypothesis that the more efficient random effects estimator is consistent at ␣ = 0 to four decimal places,
both with and without AR-1 errors.
26
Therefore our results offer only slight evidence for Republican
bias before the 17th Amendment and are largely inconclusive for
this debate (cf. King and Ellis 1996; Wirls 1999), which is not
surprising given that our design is not aimed at this issue.
SEAN GAILMARD AND JEFFERY A. JENKINS
332
Republican joint convention seat share (about one
standard deviation) increased first-dimension DWNOMINATE scores by about 45% of a standard deviation.
Yet policy preferences in the mass electorate, as expressed
in Republican presidential vote share, had a small and
insignificant effect on senators’ voting behavior.
Senators’ responsiveness to state-level political principals changed markedly after the move to direct election, in keeping with the responsiveness effect. This
change is reflected in the interaction terms. First, senators’ roll-call records became much more strongly related to Republican presidential vote shares in the state.
This is reflected in the positive and highly significant
effect of the interaction of Republican presidential vote
share and the 17th Amendment. In total after the amendment, a 15 percentage-point increase in the state Republican presidential vote share (about one standard deviation) increased first-dimension DW-NOMINATE scores
by about one-eighth of a standard deviation.
On the other hand, controlling for mass electorate
preference, senators became substantially less responsive
to the policy interests of the state legislature after the 17th
Amendment. This is reflected in the negative and highly
significant coefficient on the interaction of the amendment and Republican seat share in the state legislature.
The overall effect of Republican seat share in the state
legislature on senator DW-NOMINATE scores was significantly closer to zero, when the state legislature was no
longer explicitly a principal in the agency relationship.
Indeed, the hypothesis that the total effect of state legislature preference was zero after the amendment—that
the sum of the interacted and un-interacted coefficients
for Republican seat share in the state legislature equals
0—cannot be rejected at nearly conventional significance
levels in a likelihood ratio (␹ 2 ) test (two-tailed p-value =
0.31).
This evidence is just what one would expect based
on the responsiveness hypothesis in our principal-agent
perspective. But responsiveness engendered by electoral
institutions is only part of the accountability story. Also
relevant is the discretion of agents to pursue agendas that
depart systematically from those of either the ultimate
electoral principals or their (former) intermediaries. This
is the issue captured in Hypothesis 2, the discretion effect.
A graphical first cut at this hypothesis is presented
in Figure 1. The figure displays the absolute difference
between the first-dimension DW-NOMINATE scores for
members of a state’s Senate delegation in a given year, as
a function of its GOP presidential vote share in that year.
Aggregating over all years, the relationship is roughly
FIGURE 1 State Ideology and Within-Delegation Distance, Before
and After the 17th Amendment
In both panels within-delegation distance (DW-NOMINATE first dimension) is roughly concave with peaks near 50% GOP vote share. Postamendment distances are less clustered around
low values and more scattered on the vertical axis.
AGENCY PROBLEMS AND THE 17TH AMENDMENT
333
TABLE 2 Regression Results: Senate Delegation DW-NOMINATE (First
Dimension) Differences (log)
Explanatory Variable
FGLS
State GOP pres. vote share
–1.259
(1.247)
1.497
(1.140)
0.947
(0.812)
–1.786∗∗
(0.702)
0.549∗∗∗
(0.178)
−0.496∗∗∗
(0.187)
0.012
(0.020)
–1.780∗∗∗
(0.390)
State GOP pres. vote share, squared
GOP joint convention share
GOP joint convention share, squared
17th Amendment indicator
South indicator
Time trend
Constant
N = 585
␹ 2 = 75.3∗∗∗
OLS, State FEs
P-W, State FEs
−0.158
(1.646)
0.596
(1.425)
1.344
(1.073)
–2.046∗∗
(0.915)
0.554∗∗∗
(0.194)
–
−0.166
(1.732)
0.916
(1.561)
0.225
(1.114)
–1.267
(0.968)
0.583∗∗∗
(0.135)
–
0.014
(0.022)
–2.340∗∗∗
(0.493)
F = 8.90∗∗∗
Within R2 = 0.09
–
–2.026∗∗∗
(0.321)
F = 5.81∗∗∗
Within R2 = 0.06
Note: Unit of observation is a state-year, 1880–1940. FGLS errors are assumed to be AR-1 within a state’s
time path and heteroskedastic across states in a given year. Standard errors are in parentheses.
∗
denotes significance at ␣ = 0.10, ∗∗ at 0.05, ∗∗∗ at 0.01.
concave. Within-delegation distance is greater in moderate states than in extreme states. The key feature for
Hypothesis 2 is that conditional on state ideology, the
within-delegation distances appear larger on average after the 17th Amendment—the points are more dispersed
in the vertical dimension and less tightly packed close to
the horizontal axis. It would appear that senators postamendment no longer behave so similarly as others facing
much the same political environment.
The figure is suggestive but obscures many possible
confounds. To determine if this difference in distances
before and after the amendment is indeed significant,
we model within-delegation distance statistically. Distances cannot be negative, and the distribution of distances shows strong right-skew. We use the natural log of
within-delegation distance as the dependent variable.
Our baseline FGLS model specifies within-delegation
distance as a function of mass electorate preference, state
legislative preference, a 17th Amendment indicator variable, a South indicator, and a time trend.27 For both statelevel political principals, we include both the basic mea27
Whether a Senate delegation is a unified-party or split-party delegation also affects the within-delegation distance (cf. Poole and
Rosenthal 1984). However, as Brunell and Grofman (1998) argued,
the 17th Amendment exerted a causal effect on the prevalence of
split-party delegations, making them more common. Moreover,
sures of their preferences and their squares. This is to allow
for (but does not impose) a concave relationship between
these preferences and within-delegation distance, as depicted in Figure 1. Results of the model are presented in
Table 2.28
the moribund Republican Party in the South over much of this
period likely also had a causal effect on party splitting. Therefore,
including split-party status as a covariate in the regression models
would cause systematic downward bias on the estimated effects
of other covariates that cause party splitting: some of their effect
would work through the party-splitting variable, therefore reducing their magnitude.
By far the simplest (this footnote notwithstanding) way to avoid
this bias is to exclude party splitting as a covariate (i.e., to avoid
controlling for an intermediate outcome). This exclusion allows
consistent or unbiased (depending on the estimator) estimation
of the treatment effects of interest. Another approach is to use a
path model, a type of recursive system of equations estimable by
a two-stage procedure, which in theory should produce the same
estimated treatment effect as the basic model with exclusion. We
estimated a path model by FGLS, with a first-stage Linear Probability Model to estimate the probability of a split-party delegation
as a function of other covariates in the FGLS model for withindelegation distance. The results, which we omit for brevity, yield
a treatment effect of the 17th Amendment similar in quantitative
terms to those in Table 2 (changing the within-delegation distance
by about a fourth of a standard deviation).
28
The table also presents results from OLS and Prais-Winsten (AR1 errors within a state’s time path) models with state fixed effects.
334
Before discussing the key results for our theory we
briefly discuss the other estimates. For Republican joint
convention share, but not Republican presidential vote
share, the results reflect a generally concave relationship
with within-delegation differences (and only the statehouse composition variables are significant).29 Specifically, the linear term is positive and the quadratic term
is negative, which implies a concave shape for positive
domain values. These results are fairly consistent across
models in Table 2. Relatively extreme states tend to have
relatively extreme U.S. Senators, but moderate states have
U.S. Senators all over the ideological map. The negative
coefficient on the South indicator reveals that southern
delegations had significantly lower within-delegation differences overall (before and after the amendment) than
all delegations. Ex ante it was not obvious that this result should occur; southern delegations leaned further
left over this time period and tended to be of the same
party, which could hold down differences, but effective
one-party rule in the South could have fused quite distinct senators together in a unified Democratic delegation
with a less than fully informative party label. Finally, the
time trend, while slightly positive, is insignificant.
With respect to the increased discretion hypothesis,
the 17th Amendment was associated with a strongly significant increase in within-delegation distance, all else
constant. Direct election increased the natural log of
within-delegation distance by about 40% of a standard
deviation in the FGLS specification. For all error specifications the evidence is highly inconsistent with what
one would expect if direct election had no effect (or a
negative effect) on senatorial discretion, as measured by
within-delegation distance.
Three other pieces of evidence corroborate our conclusion about the increase in discretion following the
elimination of delegated selection and monitoring of senators. First, in our model of senator DW-NOMINATE
scores for Hypothesis 1, the increased responsiveness of
senator voting behavior to the mass electorate following
the 17th Amendment is outweighed (in standardized as
well as absolute terms) by the decrease in responsiveness
to the state legislature. Second and relatedly, the R2 in an
Hausman tests strongly reject the hypothesis that the corresponding
random effects estimators, while more efficient, are consistent.
We also check for robustness using a Generalized Linear Model,
specifying a distribution (which is right skewed) for withindelegation distances and a natural log link function. Significance
tests for the theoretically critical variables have similar results. We
omit these results for brevity.
29
It is possible that correlation between statehouse composition
and state Republican vote share makes precise estimates of each
factor difficult to obtain.
SEAN GAILMARD AND JEFFERY A. JENKINS
OLS model with state fixed effects for individual senator
DW-NOMINATE scores, estimated on the sample period
before the 17th Amendment (1880–1912), is higher than
that from the period after (1916–1940). Third, in an independent analysis, Patty (2008) has demonstrated that
predictability of DW-NOMINATE scores (measured by
the generalized mean probability of correct classification
of a senator’s yea or nay vote on any given issue) declined
after the 17th Amendment. All of these results mean that
a collection of political principals one may use to explain
senator voting behavior had less explanatory power after
the formal institution of direct election. This is in line
with the discretion effect.
Of course we cannot say whether senators are using
this increased discretion to pursue their own ideological agendas (i.e., “shirking”), develop relationships with
interest groups, assemble different reelection constituencies, etc.30 We can only say that senators appear to be less
constrained by factors in their state political scene after
the 17th Amendment than they were before it, and this
is the implication of eliminating delegated monitoring by
political experts.
In short, the empirical support for Hypothesis 2,
the discretion effect, also appears fairly robust. Taken together, the empirical arguments in this section strongly
support the agency theoretic view of the institutional
change in the 17th Amendment, and the accountability
effects of direct election.
Probing the Mechanisms of Change
The results above reveal effects coincident with the 17th
Amendment and consistent with our theory. However,
they leave open to question the precise institutional mechanisms behind these effects, and indeed whether these
mechanisms had a causal effect at all. We explore these
issues in greater depth in this section and the next.
The responsiveness and discretion effects of the 17th
Amendment could occur through several possible channels. Specifically, the changes observed may have occurred
because the amendment made it easier for a state to
send a split-party delegation to the Senate (Brunell and
Grofman 1998), because of changes in behavior within
parties, or some combination. For example, if change by
30
Levitt’s (1996) analysis would suggest all of the above, though
catering to interest groups (which arguably would be a limitation
on the discretion of senators, as they are constrained by another
factor they may find useful for winning elections) may be unlikely
before the midtwentieth century rise of the interest group system—
a development that occurs after the end of our sample period
(Baumgartner and Leech 1998).
AGENCY PROBLEMS AND THE 17TH AMENDMENT
335
established partisans is not possible, delegation splitting
could simply be a means for an electorate to make its
delegation, on average, more representative of its interests (Alesina and Rosenthal 1995), though it would simultaneously allow senators more leeway to differ from
each other and the principal selecting them. Each of these
channels is consistent with the theory, but with the basic
results established it is interesting to see if one or the other
channel can be ruled out.
To address this we estimate the FGLS responsiveness
model from Table 1 separately for Republican and Democratic U.S. Senators, and the FGLS discretion model from
Table 2 separately for unified Republican, Unified Democrat, and split-party Senate delegations. If all the results
from the fourth section were due to a shift from unified to split-party delegations, these models would reveal
no evidence supporting our theory, as they all condition
on delegation composition. The results are contained in
Tables 3 and 4.
TABLE 3 Regression (FGLS) Results: Senator
DW-NOMINATE (First Dimension)
Scores
Explanatory Variable
State GOP pres.
vote share
Interact., state GOP pres.
vote share and 17th
Amendment
GOP joint convention
share
Interact., GOP joint
convention share and
17th Amendment
17th Amendment
indicator
South indicator
Time trend
Republican
Democrat
0.014
(0.054)
0.759∗∗∗
(0.094)
0.001
(0.089)
0.225∗∗
(0.106)
0.108∗∗∗
(0.036)
−0.298∗∗∗
(0.054)
0.077
(0.052)
0.164∗∗∗
(0.059)
−0.286∗∗∗
(.051)
0.128∗∗∗
(0.036)
0.006∗∗
(0.003)
0.263∗∗∗
(0.043)
−0.071∗
(0.040)
−0.075∗∗∗
(0.018)
0.027∗∗∗
(0.002)
−0.625∗∗∗
(0.041)
Both within-party responsiveness models are consistent with three key implications of the theory. First, for
neither Republicans nor Democrats is a senator’s scaled
roll call significantly related to state Republican presidential vote share. The p-values of 0.80 for Republicans and
0.99 for Democrats are large enough to suggest that Type
II errors are not a serious concern here. Second, roll calls
for both Republican and Democratic senators did become
significantly more responsive to partisan leanings in the
state electorate after the 17th Amendment. Two more
implications hold for Republicans but not Democrats:
roll calls for Republican senators became less responsive
to statehouse composition after the 17th Amendment;
and Republican senator roll calls are significantly related
to statehouse composition before passage of the amendment. However, Democratic senators were not significantly responsive to statehouse composition prior to the
17th Amendment and became significantly responsive after it. It is not clear why this should be so; one possibility is
that effective one-party rule in solidly Democratic states
muted responsiveness before 1914, while better sorting of
politicians into parties from 1914 to 1940 affected both
state legislatures and Senate delegations simultaneously.
These exceptions notwithstanding, analysis within parties shows support for our theory only somewhat weaker
than the overall analysis. This suggests that two distinct
channels, modification of behavior within parties and increasing likelihood of split-party delegations, each make
a contribution to the observed effect.31
The within-party discretion models also reveal effects similar to the overall results. For unified Republican and split-party delegations, the 17th Amendment is
associated with a positive, significant increase in withindelegation differences in scaled roll calls. For Democratic
delegations, the amendment has an insignificant effect.
However, this is at least partly because so many unified
Democratic delegations from 1880 to 1940 were from the
South (about 65%), where near one-party rule meant that
common partisanship could mask great differences. For
Democratic delegations outside the South, the effect of the
amendment jumps from −0.04 to 0.48, though the latter
estimate slightly misses conventional significance levels.32
N = 558
␹ 2 = 506.58∗∗∗
31
Note that the 17th Amendment indicator is negative and significant within each party. This suggests, distinct from Republican
bias before the 17th Amendment (cf. footnote 26), a sort of “rightleaning bias” within each party. While an interesting possibility, this
is beyond the scope of our article, and we defer further exploration
for future research.
Note: Unit of observation is a senator-state-year, 1880–1940. FGLS
errors are assumed to be AR-1 within a state’s time path and
heteroskedastic across states in a given year. Standard errors are in
parentheses.
∗
denotes significance at ␣ = 0.10, ∗∗ at 0.05, ∗∗∗ at 0.01.
32
Note, therefore, that including southern states creates a “hard test”
for the discretion models because the party label is less informative
about positions. We choose to retain southern observations in the
models in general because it makes the analysis somewhat more
circumspect.
Constant
N = 629
␹ 2 = 138.14∗∗∗
SEAN GAILMARD AND JEFFERY A. JENKINS
336
TABLE 4 Regression (FGLS) Results: Senate Delegation DW-NOMINATE
(First Dimension) Differences
Explanatory Variable
State GOP pres. vote share
State GOP pres. vote share, squared
GOP joint convention share
GOP joint convention share, squared
17th Amendment indicator
South indicator
Time trend
Constant
Republican
Delegations
Democratic (NonSouthern) Delegations
Split-party
Delegations
1.607
(2.278)
−0.214
(1.786)
1.126
(1.429)
–1.464
(1.149)
0.347∗
(0.194)
–
2.068
(7.207)
–3.574
(7.414)
3.584∗∗
(1.457)
–3.319∗∗
(1.749)
0.477
(0.368)
–
−0.009
(0.025)
–3.299∗∗∗
(0.628)
0.091∗∗∗
(0.032)
–4118∗∗
(1.639)
4.978∗∗∗
(1.746)
–4.772∗∗∗
(1.383)
−0.382
(0.552)
0.111
(0.449)
0.440∗∗∗
(0.140)
−0.426∗∗
(0.178)
−0.061∗∗∗
(0.014)
–1.094∗∗∗
(0.521)
N = 238
␹ 2 = 18.87∗∗∗
N = 75
␹ 2 = 120.87∗∗∗
N = 129
␹ 2 = 44.03∗∗∗
Note: Unit of observation is a state-year, 1880–1940. FGLS errors are assumed to be AR-1 within a state’s
time path and heteroskedastic across states in a given year. Standard errors are in parentheses.
∗
denotes significance at ␣ = 0.10, ∗∗ at 0.05, ∗∗∗ at 0.01.
To be sure, part of the effect of the 17th Amendment on
within-delegation difference in Table 2 is due to shifts
from unified-party to split-party delegations. However,
as with responsiveness, the discretion results conditional
on delegation type suggest that at least part of the effects
uncovered in Table 2 are due to changes within each delegation type, and not entirely because of shifts among the
delegation types.
These results also help to compare our theoretical explanation to an alternative account based on partisan gerrymanders in state legislative districts. In particular, these
gerrymanders made state legislatures more homogenous
than the state electorate in terms of partisanship, and
much more likely to choose unified-party U.S. Senate
delegations. The 17th Amendment can be understood
as a shift in the median voter of a senator’s electorate
from the median of the state legislature to the median
of the electorate. While gerrymandered state legislatures
typically chose unified-party delegations, the state electorate did not have to (and indeed did so significantly
less often than state legislatures; see Brunell and Grofman
1998). With state voters choosing split-party Senate delegations more often, the Senate delegation would be more
responsive to voters on average and would exhibit larger
within-delegation differences after the amendment. This
is a compelling argument based on the historical circumstances and at a broad level matches up with the evidence.
However, we contend that our account is preferable for
three reasons. First, it has more explicit foundations in
agency theory, which clarify its logic in the abstract and
also its linkage to other findings on electoral institutions.
Second, by tying our Hypotheses 1 and 2 together in a single theory, our account also has broader empirical implications than this alternative, and therefore more grounds
to be falsified. It is therefore all the more powerful because it is not in fact falsified in a battery of empirical
tests. Third, this alternative account is unable to fully account for our findings, because it depends entirely on a
shift toward split-party U.S. Senate delegations after the
17th Amendment. As Tables 3 and 4 show, the results are
consistent with our account even conditional on delegation type.
Another important question about the institutional
mechanism behind the results above deals with the date
of the “treatment” whose effect we seek. Our theoretical perspective is based on direct election, not the 17th
AGENCY PROBLEMS AND THE 17TH AMENDMENT
Amendment per se. For us as for other scholars who
have recently identified effects related to the 17th Amendment, the amendment is simply a convenient vehicle for
analysis of our theoretical concern. As noted, several
scholars (e.g., Riker 1955; Rogers 1926) have argued
that the amendment was an anticlimactic codification
of changes that were actually effected by prior electoral
reforms at the state level, i.e., binding direct primaries.33
Lapinski (2003) has authoritatively established dates of
these reforms for each state.34 We have replicated all of
our substantive and statistical conclusions using a state’s
date of adoption of any sort of (binding) direct primary
of senators as the date of its treatment,35 rather than the
nationwide ratification of the 17th Amendment. None of
our conclusions, substantive or statistical, is altered by
defining the treatment in this way. The main reason for
this is that, of the states that adopted binding links between the mass electorate and the selection of senators,
almost all of them did so after 1900, and most in 1907 or
later. Thus, however the treatment date is defined, most
pre- and posttreatment observations are identical. We discuss our main results with the 17th Amendment itself as
the treatment, rather than states’ primary-election adoption dates, because the amendment is a more focal (and
legally binding) change and has the virtue of being an
exogenous treatment for at least some states.36
33
Of course, to the extent that the 17th Amendment only ratified reforms that individual states had already made before 1914,
finding evidence of these implications should be difficult. Stated
differently, if the amendment really amounted to nothing more
than a codification, we would find a null effect of the amendment
empirically.
34
Lapinski (2003) also makes a persuasive case against these statelevel direct primary laws truly mimicking direct election. The laws
themselves could not be legally binding, Lapinski argues, as the
direct agency relationship between state legislatures and U.S. Senators was spelled out in the U.S. Constitution. Moreover, the vast
majority of states that passed direct-primary laws also were on the
forefront of convention calls, i.e., petitions to Congress calling for
a convention to alter the Constitution and include a direct-election
amendment.
35
Some states before the 17th Amendment had voluntary agreements by political parties to honor results of statewide popular
vote in selection of U.S. Senators. We do not consider these to be as
constraining as formal institutional changes and do not use them
in defining the alternative treatment dates. In any case, only a few
states took this approach before the 17th Amendment, and most
only shortly before it.
36
Another possible alternative treatment is the adoption of the
Australian Ballot, which helped to wrest control of nominations
for national political office generally (not just the Senate) from
hard-core partisans and ideologues. When we use Australian Ballot
adoption dates within states as a treatment date, the treatment has
essentially no effect on responsiveness or discretion. This makes
sense because Australian Ballot adoption tended to occur somewhat
far in advance of direct election or the 17th Amendment. Our data
337
Beyond simply dating the treatment or parsing it
out among parties and delegation types is a deeper issue of what the treatment actually is. Given the quasiexperimental nature of the research design, it is conceivable in principle that other institutional changes in the
U.S. Senate at this time are simply reflected in our results
as “effects” of the 17th Amendment. Three conspicuous
cases of major institutional change in the Senate are cloture reform, the rise of formal Senate leadership, and
the further institutionalization of the committee system.
Nevertheless it is not clear how these factors could individually or jointly produce the combination of results we
observe. Cloture reform might have affected the blocking
power of minority coalitions and conceivably therefore
the agenda over which roll calls are taken. However, we
are not aware of any compelling reason why it would
affect responsiveness and discretion consistent with our
empirical findings above, and recent theoretical treatments (Wawro and Schickler 2006) have not offered any.
The rise of the Senate party leadership in the first decades
of the twentieth century (Campbell, Cox, and McCubbins 2002; Gamm and Smith 2004) is another important
change. This might have, if anything, constrained member behavior as leaders coordinated or even compelled
votes (or restricted the agenda to issues on which the
party was cohesive), thereby holding together the behavior of otherwise different senators from a given state.
Such an effect would work against the discretion results
we observe; again, it is not clear what effect if any this
change should have had on responsiveness.37 Finally, Senate committees achieved new institutionalization over the
time period we study. With any degree of self-selection
it seems likely that committees could expand observed
differences in specialization of senators and possibly roll
calls. At the same time, because of the same self-selection
it is not clear that committees would cause such differences rather than reflect ones that already exist. Moreover,
as with the other changes, we cannot identify any natural reason why responsiveness should have been affected
by committee development. Overall, then, while other
institutional developments occurred in the Senate contemporaneous with the 17th Amendment, they do not
essentially allow a test of the conjecture that the “real” treatment
is the Australian Ballot; if this were the case null results for the
Australian Ballot and nonnull results for the 17th Amendment
are the opposite of the expected pattern. Moreover, the Australian
Ballot is not a Senate-specific change, but presumably affected the
House of Representatives too; it is at least in part addressed by the
“placebo test” we execute for the House in the sixth section below.
37
Of course even now it is far from clear that Senate party leaders
have the means to constrain senator behavior; moreover, as Gamm
and Smith (2004) note, Senate party leadership did not fully solidify
until the 1930s.
338
appear immediately credible as alternatives to the institutional mechanism of direct election in accounting for the
empirical patterns we identify.
The institutionalization of party leadership and committees is actually not unique to the Senate in the time
period we study. These institutional changes and many
others—to name a few, the rise of presidential primaries,
the resurgence of the Democratic Party in presidential
politics, changing alignments of social and economic
coalitions with the two major parties, the Progressive
Era, the Australian Ballot, and the 19th Amendment—
occurred in the larger political narrative of this era as a
whole. These developments all occurred at or near the
adoption of the 17th Amendment. If some such factor or
combination of them were actually driving the empirical
results above, we might inadvertently attribute its effects
to the 17th Amendment and incorrectly consider the theory in this article to be a useful one for explaining the
effects of the institutional change to direct election.
Importantly, these and many other contemporaneous, potentially confounding political developments are
not Senate specific. They should also affect the U.S. House
of Representatives, which is therefore a useful comparison
case: it was not directly affected by the treatment we explore, but was affected by potentially confounding events.
Does the 17th Amendment “Explain”
Changes in the House
of Representatives?
If the move to direct election caused the changes in Senate
representation we identified above, then the 17th Amendment should not be associated with similar changes in the
House. Conversely, if the amendment “explains” changes
in the House as well as the Senate, the empirical support
for our theory would be weaker.
We applied the same statistical models employed
above to the U.S. House over the same time period. We
find that the 17th Amendment is not associated with
changes in House roll-call records similar to those that we
found for the Senate. This is as expected assuming that the
amendment, rather than a contemporaneous confounding factor, caused the changes we identified above for the
Senate. This strongly suggests that our results for the Senate are not merely picking up some other factor unrelated
to the change in the political agency relationship.
First consider Hypothesis 1, the responsiveness effect
in the House. While House members should be responsive
to several state interests, they should not be more or less
so directly because of the 17th Amendment. We take each
SEAN GAILMARD AND JEFFERY A. JENKINS
state-year as the unit of analysis, for presidential election
years from 1880 to 1940. The dependent variable is the
average first-dimension DW-NOMINATE score for all
members of a state’s U.S. House delegation (mean = 0.10,
standard deviation = 0.35).38
The two crucial features of the responsiveness effect work out as follows. First, since House members
have always been chosen by direct election, their average DW-NOMINATE score should be positively related
to the state’s Republican share of the two-party presidential vote. However, our theory predicts that that relationship should not be any different after the passage
of the 17th Amendment than before it. Second, the state
U.S. House delegation’s average DW-NOMINATE score
should also be positively related to the Republican share
of seats in the state legislature. This is because of control over congressional district lines and the possibility
of partisan gerrymanders (Engstrom 2006): as one party
increased its dominance in the state legislature, it had
more control over districts and better ability to see its
ideals carried into Congress. However, this effect did not
systematically change with the 17th Amendment (especially controlling for a time trend), so the relationship
between state legislature composition and House average
DW-NOMINATE score should not differ before and after
the 17th Amendment.
The results in Table 5 from feasible GLS regression
are consistent with these expectations. U.S. House delegations are responsive in their roll-call voting to the Democratic/Republican leanings of the state electorate. But the
interaction of Republican presidential vote share and the
17th Amendment indicator shows that they are no more
or less responsive after the amendment. Similarly, U.S.
House delegations are responsive to the partisan composition of the state legislature—but again no more or less
so after the 17th Amendment.39
Bearing on Hypothesis 2, the discretion effect, we
also find that the 17th Amendment is not associated with
systematic changes in the within-delegation distance in
38
Paucity of reliable congressional district level on election returns,
or a natural benchmark comparison in the state legislature, precludes the use of congressional districts as the units of observation.
39
These results are very similar to those obtained from pooled
OLS with state fixed effects and pooled Prais-Winsten regression
with state fixed effects and AR-1 errors within panels. (In both of
these cases Hausman tests reject consistency of the random effects
estimator.) The fixed-effects results are also in Table 5. One anomaly
is that the 17th Amendment indicator variable has a marginally
significant positive effect on the House delegation average in the
autoregressive fixed-effects regression. However, based on the other
models it appears to be an isolated occurrence and not surprising
given the great chance of a false positive occurring at least once in
this article. In any case, the main effect of the 17th Amendment is
not a key implication of the responsiveness hypothesis.
AGENCY PROBLEMS AND THE 17TH AMENDMENT
339
TABLE 5 Regression Results: House Delegation DW-NOMINATE (First
Dimension) Average
Explanatory Variable
State GOP pres. vote share
Interact., state GOP pres. vote
share and 17th Amendment
GOP joint convention share
Interact., GOP joint convention
share and 17th Amendment
17th Amendment indicator
South indicator
Time trend
Constant
N = 613
OLS,
State FEs
Prais-Winsten,
State FEs
0.146∗
(0.086)
−0.060
(0.118)
0.723∗∗∗
(0.052)
−0.091
(0.066)
0.044
(0.045)
−0.199∗∗∗
(0.025)
0.015∗∗∗
(0.003)
0.427∗∗∗
(0.047)
0.301∗∗∗
(0.099)
0.039
(0.144)
0.554∗∗∗
(0.060)
−0.155
(0.181)
0.115
(0.158)
–
0.190∗
(0.111)
0.061
(0.154)
0.508∗∗∗
(0.068)
−0.075
(0.088)
0.095∗
(0.054)
–
0.014∗∗∗
(0.003)
0.470∗∗∗
(0.054)
−0.268∗∗∗
(0.035)
␹ 2 = 2282.4∗∗∗
F = 49.1∗∗∗
Within R2 = 0.34
F = 35.4∗∗∗
Within R2 = 0.25
FGLS
–
Note: Unit of observation is a state-year, 1880–1940. FGLS errors are assumed to be AR-1 within a state’s
time path and heteroskedastic across states in a given year. Standard errors are in parentheses.
∗
denotes significance at ␣ = 0.10, ∗∗ at 0.05, ∗∗∗ at 0.01.
the U.S. House. Here again we take state-years as the unit
of analysis, in presidential election years from 1880 to
1940. As the dependent variable, we take the interquartile
range of first-dimension DW-NOMINATE scores for the
state’s U.S. House delegation in a given year (mean = 0.19,
standard deviation = 0.23).40 Since the 17th Amendment
should not have affected discretion of House members
with respect to their principals in the state electorate,
our theory predicts no effect of the 17th Amendment on
within-delegation distance. The FGLS results in Table 6
below show that the evidence is consistent with this prediction. The p-value on the 17th Amendment indicator is
too large (two-tailed p = 0.93) to make this assumption
of no effect appear suspect.41
These findings show that the 17th Amendment is not
associated with changes in responsiveness or discretion of
House members. This is not the pattern one would expect
if the observed changes in the Senate were actually the
result of broader political forces rather than the institution
of direct election.
Conclusion
40
Since most states have many more than two congressional districts, using the maximum distance as in the Senate case would
create a measure badly skewed by outliers in many state-years. The
interquartile range is less sensitive to such issues, as it is based on
order statistics.
Our theory of the agency relationship between the mass
electorate and U.S. Senators before and after the 17th
Amendment implies that direct election had both a benefit and a cost. The amendment clearly made senators responsive directly to state electorates, so their selection and
accountability once in office were based on a democratically stronger standard. At the same time, the amendment
made senators answerable to relative political novices, so
they could not be held to that standard (whether through
electoral sanctioning or selection) as tightly as they were
41
These results are again identical in qualitative and statistical significance terms to those obtained from OLS regression with state
fixed effects and Prais-Winsten regression with state random effects
and AR-1 errors within panels (also in Table 6). In the latter case,
a Hausman test does not reject the hypothesis that the random
effects estimator is consistent. Since the RE estimator is necessarily
more efficient than the FE, we prefer it in this case.
SEAN GAILMARD AND JEFFERY A. JENKINS
340
TABLE 6 Regression Results: House Delegation DW-NOMINATE (First
Dimension) Interquartile Range
Explanatory Variable
State GOP pres. vote share
State GOP pres. vote share, squared
GOP joint convention share
GOP joint convention share, squared
17th Amendment indicator
South indicator
Time trend
Constant
N = 612
FGLS
OLS, State FEs
P-W, State REs
0.078
(0.102)
−0.123
(0.107)
0.564∗∗∗
(0.104)
−0.532∗∗∗
(0.093)
0.002
(0.022)
0.042
(0.029)
−0.0001
(0.002)
0.020
(0.046)
0.146
(0.226)
−0.204
(0.196)
0.666∗∗∗
(0.149)
−0.662∗∗∗
(0.127)
0.026
(0.026)
–
0.182
(0.222)
−0.238
(0.194)
0.694∗∗∗
(0.145)
−0.681∗∗∗
(0.125)
0.011
(0.016)
−0.003
(0.062)
–
␹ 2 = 47.7∗∗∗
−0.001
(0.003)
0.072
(0.068)
0.040
(0.068)
F = 6.4∗∗∗
Within R2 = 0.06
␹ 2 = 42.5∗∗∗
Overall R2 = 0.12
Note: Unit of observation is a state-year, 1880–1940. FGLS errors are assumed to be AR-1 within a state’s
time path and heteroskedastic across states in a given year. Standard errors are in parentheses.
∗
denotes significance at ␣ = 0.10, ∗∗ at 0.05, ∗∗∗ at 0.01.
held to their preamendment standard. The trade-off is
analogous to comparing two estimators, one having lower
bias but greater variance than the other. Our empirical results show that the implications of this view do appear in
senator behavior and that it is helpful in understanding
the agency relationship between the mass electorate, its
expert political intermediaries, and its U.S. Senate delegation. The same patterns do not appear in the House of
Representatives, ruling out more general contemporaneous factors unrelated to direct election as an explanation
for our finding. In short, we found an effect of the treatment on treated units that is in line with our theory and
did not find an effect of the treatment on untreated units.
Theoretically, the trade-off we identify between responsiveness and monitoring is an important consideration for the design of electoral institutions. Even the
17th Amendment itself appears in contemporary policy
debates occasionally: for example, within the last several
years, senator Zell Miller (D-GA) introduced a measure
in the Senate calling for its repeal (Pierce 2004),42 and
Alan Keyes made its repeal part of his platform in the
Illinois race for the U.S. Senate in 2004 (Pearson 2004).
42
Less than a week before Miller’s motion, Rep. Tom DeLay (R-TX)
came out against the 17th Amendment and stated that he would
be willing to discuss its repeal (Pierce 2004).
In the end, however one comes down on the trade-off
created by direct agency, our theory and results show it
does matter for representation and the interests that get
reflected in public policy.
References
Alesina, Alberto, and Howard Rosenthal. 1995. Partisan Politics,
Divided Government, and the Economy. New York: Cambridge University Press.
Arnold, R. Douglas. 1993. “Can Inattentive Citizens Control
Their Representatives?” In Congress Reconsidered, 5th ed.,
ed. Lawrence Dodd and Bruce Oppenheimer. Washington,
DC: Congressional Quarterly Press, 401–16.
Banks, Jeffrey S., and Rangarajan Sundaram. 1993. “Adverse Selection and Moral Hazard in a Repeated Elections Model.”
In Political Economy: Institutions, Competition, and Representation, ed. William Barnett, Melvin Hinich, and Norman
Schofield. New York: Cambridge University Press, 295–311.
Banks, Jeffrey S., and Rangarajan Sundaram. 1998. “Optimal
Retention in Agency Problems.” Journal of Economic Theory
82(2): 293–323.
Barro, Robert. 1973. “The Control of Politicians: An Economic
Model.” Public Choice 14: 19–42.
Bartels, Larry. 1991. “Constituency Opinion and Congressional
Policy-making: The Reagan Defense Buildup.” American Political Science Review 85(2): 457–74.
AGENCY PROBLEMS AND THE 17TH AMENDMENT
Baumgartner, Frank, and Beth Leech. 1998. Basic Interests.
Princeton, NJ: Princeton University Press.
Beck, Nathaniel, and Jonathan Katz. 1995. “What to Do (and
Not Do) with Time Series-Cross Section Data.” American
Political Science Review 89(3): 634–47.
Bernhard, William, and Brian R. Sala. 2006. “The Remaking of
an American Senate: The 17th Amendment and Ideological
Responsiveness.” Journal of Politics 68(2): 345–57.
Besley, Timothy, and Anne Case. 2003. “Political Institutions
and Policy Choices: Evidence from the United States.” Journal of Economic Literature 41(1): 7–73.
Besley, Timothy, and Stephen Coate. 2003. “Elected versus Appointed Regulators: Theory and Evidence.” Journal of the
European Economic Association 1(5): 1176–1206.
Brady, David W. 2006. “Rational Choice, History, and the Dynamics of Congress.” In The Macropolitics of Congress, ed. E.
Scott Adler and John S. Lapinski. Princeton, NJ: Princeton
University Press, 251–58.
Brunell, Thomas, and Bernard Grofman. 1998. “Explaining Divided U.S. Senate Delegations, 1788–1996: A Realignment
Approach.” American Political Science Review 92(2): 391–99.
Burnham, Walter Dean. 1984. Partisan Division of American
State Governments, 1834–1985 [Computer file]. Conducted
by Massachusetts Institute of Technology. ICPSR ed. Ann
Arbor, MI: Inter-university Consortium for Political and
Social Research.
Campbell, Andrea, Gary Cox, and Mathew McCubbins. 2002.
“Agenda Power in the U.S. Senate, 1877–1986.” In Party
Process and Political Change in Congress, ed. David Brady
and Mathew McCubbins. Stanford, CA: Stanford University
Press, 218–47.
Campbell, Angus, Philip E. Converse, Warren E. Miller, and
Donald E. Stokes. 1960. The American Voter. New York: John
Wiley and Sons.
Campbell, Ballard. 1980. Representative Democracy: Public Policy and Midwestern Legislatures in the Late Nineteenth Century. Cambridge, MA: Harvard University Press.
Canes-Wrone, Brandice, David W. Brady, and John Cogan.
2002. “Out of Step, Out of Office: Electoral Accountability and House Members’ Voting.” American Political Science
Review 96(1): 127–40.
Carson, Jamie L. 2005. “Strategy, Selection, and Candidate
Competition in U.S. House and Senate Elections.” Journal
of Politics 67(1): 1–28.
Carson, Jamie L., and Jeffery Jenkins. 2007. “Examining the
Electoral Connection across Time.” Working paper. University of Virginia.
Crook, Sara Brandes, and John Hibbing. 1997. “A Not So Distant Mirror: The Senate and Congressional Change.” American Political Science Review 91(4): 845–53.
Downs, Anthony. 1957. An Economic Theory of Democracy. New
York: Harper & Row.
Engstrom, Erik. 2006. “Stacking the States, Stacking the House:
The Politics of Congressional Redistricting in the 19th Century.” American Political Science Review 100(3): 419–27.
Engstrom, Erik, and Samuel Kernell. 2007. “The Effects of Presidential Elections on Party Control of the Senate under Direct and Indirect Elections.” In Party, Process, and Political
Change in Congress, Volume 2: Further New Perspectives on
341
the History of Congress, ed. David W. Brady and Mathew D.
McCubbins. Stanford, CA: Stanford University Press, 37–52.
Erikson, Robert S., and Gerald C. Wright. 2000. “Representation
of Constituency Ideology in Congress.” In Continuity and
Change in House Elections, ed. David Brady, John Cogan,
and Morris Fiorina. Stanford, CA: Stanford University Press,
148–77.
Fearon, James. 1999. “Electoral Accountability and the Control of Politicians: Selecting Good Types versus Sanctioning
Poor Performance.” In Democracy, Accountability, and Representation, ed. Adam Przeworski, Susan Stokes, and Bernard
Manin. New York: Cambridge University Press, 55–97.
Ferejohn, John. 1986. “Incumbent Performance and Electoral
Control.” Public Choice 50(1): 5–25.
Gamm, Gerald, and Steve Smith. 2004. “Floor Leadership and
the Rise of the Modern Senate, 1899–1937.” Presented at the
annual meeting of the Midwest Political Science Association.
Hall, Melinda Gann. 2001. “State Supreme Courts in American
Democracy: Probing the Myths of Judicial Reform.” American Political Science Review 95(2): 315–30.
Hanssen, F. Andrew. 1999. “The Effect of Judicial Institutions on
Uncertainty and the Rate of Litigation: The Election versus
Appointment of State Judges.” Journal of Legal Studies 28(1):
205–32.
Haynes, George H. 1906. The Election of Senators. New York:
Henry Holt.
Haynes, George H. 1938. The Senate of the United States. New
York: Russell & Russell.
Kernell, Samuel. 2005. “The Responsiveness of State Legislative Elections in the Late 19th and Early 20th Centuries.”
Presented at the annual meeting of the American Political
Science Association.
King, Ron, and Susan Ellis. 1996. “Partisan Advantage and Constitutional Change: The Case of the Seventeenth Amendment.” Studies in American Political Development 10(1): 69–
102.
Lapinski, John S. 2003. “The Behavioral and Institutional Effects
of Direct Election.” Presented at the annual meeting of the
American Political Science Association, Philadelphia.
Levitt, Steven D. 1996. “How Do Senators Vote? Disentangling
the Role of Voter Preferences, Party Affiliation, and Senator
Ideology.” American Economic Review 86(3): 425–41.
Lupia, Arthur, and Mathew D. McCubbins. 1998. The Democratic Dilemma: Can Citizens Learn What They Need to Know?
New York: Cambridge University Press.
Meinke, Scott R. 2008. “Institutional Change and the Electoral
Connection in the Senate: Revisiting the Effects of Direct
Election.” Political Research Quarterly 61(3): 445–57.
Miller, Warren, and Donald Stokes. 1963. “Constituency Influence in Congress.” American Political Science Review 57(1):
45–56.
Patty, John. 2008. “Equilibrium Party Government.” American
Journal of Political Science 52(3): 636–55.
Pearson, Rick. 2004. “Keyes Says Game Plan Is Controversy.”
Chicago Tribune, September 14, 2004.
Pierce, Greg. 2004. “Inside Politics.” Washington Times, April
30, 2004.
Poole, Keith T., and Howard Rosenthal. 1984. “The Polarization
of American Politics.” Journal of Politics 46(4): 1061–79.
342
Poole, Keith T., and Howard Rosenthal. 1997. Congress: A Political Economic History of Roll Call Voting. New York: Oxford
University Press.
Poole, Keith T., and Howard Rosenthal. 2001. “D-NOMINATE
after 10 Years: An Update to Congress: A Political-Economic
History of Roll Call Voting.” Working paper. Tepper School
of Business, Carnegie Mellon University.
Popkin, Samuel. 1991. The Reasoning Voter. Chicago: University
of Chicago Press.
Riker, William. 1955. “The Senate and American Federalism.”
American Political Science Review 49(2): 452–69.
Rogers, Lindsay. 1926. The American Senate. New York:
Knopf.
Schiller, Wendy. 2000. Partners and Rivals: Representation in
U.S. Senate Delegations. Princeton, NJ: Princeton University
Press.
SEAN GAILMARD AND JEFFERY A. JENKINS
Schiller, Wendy, and Charles Stewart III. 2007. “Challenging the Myths of 19th Century Party Dominance: Evidence from Indirect Senate Elections, 1871–1913.” Presented
at the annual meeting of the American Political Science
Association.
Schiller, Wendy, and Charles Stewart III. 2008. “The Effect of
Party Loyalty on the Election of U.S. Senators, 1871–1913.”
Presented at the annual meeting of the American Political
Science Association.
Wawro, Gregory, and Eric Schickler. 2006. Filibuster: Obstruction and Lawmaking in the U.S. Senate. Princeton, NJ: Princeton University Press.
Wirls, Daniel. 1999. “Regionalism, Rotten Boroughs, Race, and
Realignment: The Seventeenth Amendment and the Politics
of Representations.” Studies in American Political Development 13(1): 1–30.